Can information about risk alter risky behaviour?

Why do people engage in risky behaviour, like drink-driving, or risky sexual behaviour? In theory, if people are rational, they weigh up the costs and benefits of each action, and undertake actions only when the benefits of the action outweigh the costs. People who engage in risky behaviour look (to a rational observer) like they are engaging in behaviour where the costs (including an assessment of the risk) likely outweigh the benefits. Why do they do it?

I see two potential explanations here. First, perhaps this is a case of behaviour that is boundedly rational. The people engaging in the risky behaviour may not have accurate information about the costs of the behaviour, and underestimate those costs. Making their decision based on the benefits and (underestimated) costs makes them more likely to engage in the risky behaviour. Second, perhaps these people are quasi-rational, and one of the characteristics of quasi-rational decision-making (as I discuss in my ECONS102 class) is a tendency to heavily discount the future. In cases where the benefits of a risky activity occur now, but the costs are faced at some point in the future (and so, heavily discounted), a quasi-rational decision-maker may be more likely to engage in the risky behaviour.

Either of those explanations may account for risky behaviour like drink-driving, or risky sexual behaviour. If people are unaware of, or discount the value of, the full costs of drink-driving or risky sexual behaviour, they may be more likely to engage in those activities. Also, the costs of drink-driving (such as harm to themselves, or others, or property, or the risk of penalties if they are caught) occur in the future, as do the costs of risky sexual behaviour (such as the risk of a sexually-transmitted disease, or unwanted pregnancy), while the benefits occur immediately.

Which explanation accounts for more of the activity? This is unclear. However, if most risky activity is explained by a lack of accurate information, then there is an obvious policy solution: provide accurate information about the risks and costs of the activity. If most risky activity is explained by discounting the future, then it would be more difficult to address the behaviour easily with a policy solution.

That brings me to this 2018 article by Pascaline Dupas (Stanford University), Elise Huillery (University of Paris-Dauphine), and Juliette Seban (Sciences Po), published in the Journal of Economic Behavior and Organization (ungated earlier version here). They report on a randomised experiment conducted with teenage schoolgirls in Cameroon, where they provided information about the risks of unprotected sex, and measured the effect on health outcomes and teen pregnancy rates. Specifically:

We use a field experiment conducted with teenage girls in 318 junior high schools in Cameroon to study, within one context, how the type of risk information being provided and the delivery method (teacher, outside professional or questionnaire) affect adolescents knowledge, perceived risks and behavior... We randomized HIV and sexual education interventions that differed in their delivery mechanism and intensity, as well as content, across schools. In each school, one eighth grade class was targeted for the study.

We consider four interventions. The first (In-Class Quiz) was completely “hands-off”, and not labeled as an educational intervention: students were simply asked to fill in an anonymous questionnaire with questions on HIV as well as on their own sexual behavior and that of their peers. The questionnaire took about one hour to go through, including the time to introduce it. The In-Class Quiz was a group-administered questionnaire and did not provide students with direct information, but required that students think actively about risk levels...

The other three interventions were clearly labeled as HIV education programs. Two of them consisted of general information on HIV prevention methods (abstinence, faithfulness and condom use) and the average HIV prevalence at the national level (the “basic message”). A third one mimicked the “sugar daddy risk information” first proposed in Dupas (2011) and included, on top of the basic message, detailed information on HIV prevalence disaggregated by gender and age group and a special module on cross-generational relationships, locally known as relationships with “sponsors”, and their contribution to the spread of HIV. The difference between the two “basic message” interventions is that one was delivered through regular school staff which received special training (Teacher Training), while the second one was delivered by an outside consultant who did a special visit to the school to deliver the message (Consultant). The intervention that included the sugar daddy module was also delivered by an outside consultant (Consultant +). Both interventions by consultants lasted approximately one hour.

Since classes were randomised to receive one of the four treatments, comparisons across the treatments (at the class level) provide an assessment of the impact of the intervention. The primary outcome was self-reported pregnancy measured 9-12 months after the treatment. Dupas et al. found that:

...all interventions were successful at reducing the incidence of teenage pregnancy during our follow-up period. The magnitude of the effects are relatively large, with an average drop of 2.9% points in the likelihood of having started childbearing at the time of the endline, off a mean in the control group of 9.5%, thus a 30% reduction.

So, score one for information as an intervention to reduce risky behaviour! Except that:

The most surprising results is that the most hands-off intervention, the In-Class Quiz, was successful, by itself, at reducing the incidence of unprotected sex and hence pregnancy in the following 12 months.

The in-class quiz provided no information, and only asked the participants to reflect on risk. So, what happened? Dupas et al. look into the mechanisms, finding that:

...interventions increased the likelihood that girls report adopting a clear, one-pronged strategy against HIV: abstinence...

Importantly, the mechanism through which the interventions helped girls adopt a clear and simple strategy against HIV differs between the In-Class Quiz and the education interventions. The In-Class Quiz led participants to revise upward their subjective beliefs about risk, while the other interventions improved knowledge without changing risk perceptions... In contrast, the education interventions did not change perceived risks (it did not make them even more pessimistic as the Quiz, but it did not bring them much closer to reality either), but it did affect girls’ knowledge about HIV transmission and prevention. In our context, these two mechanisms (change in subjective beliefs about risk and change in knowledge) turnout to be equally effective at changing girls’ plans and behaviors.

So, it wasn't just information about risk that mattered, but making the risks more salient as well. When people are provided with information about risk, it has to make the risks seem more important, if we want them to change their behaviour. However, there is reason to be sceptical about this single study. As anyone who has tried any information intervention can tell you, simply providing people with information will almost always have little to no effect on behaviour (although David Evans enumerates a number of counter-examples here). So, we should be cautious before we proclaim that we have the ultimate solution to risky behaviour (and, to be fair, the authors don't claim this), until this study has been replicated in other settings.

Do payday loans make consumers worse off?

Back in 2020, I wrote a post about the consequences of banning payday loans on the pawnbroking industry. The takeaway message was that banning payday loans simply shifted borrowers into borrowing from pawnbrokers, small-loan lenders and second-mortgage licensees, none of which was necessary good for the borrowers. This new article by Hunt Allcott (Microsoft Research) and co-authors, forthcoming in the journal Review of Economic Studies (ungated earlier version here), looks at a related question: How would payday lending restrictions affect consumer welfare?

Allcott et al. start by undertaking a field experiment and related survey with clients of a large payday lending provider in Indiana. As Allcott et al. explain:

Our experiment ran from January to March 2019 in 41 of the Lender’s storefronts in Indiana, a state with fairly standard lending regulations. Customers taking out payday loans were asked to complete a survey on an iPad. The survey first elicited people’s predicted probability of getting another payday loan from any lender over the next eight weeks. We then introduced two different rewards: “$100 If You Are Debt-Free,” a no-borrowing incentive that they would receive in about 12 weeks only if they did not borrow from any payday lender over the next eight weeks, and “Money for Sure,” a certain cash payment that they would receive in about 12 weeks. We measured participants’ valuations of the no-borrowing incentive through an incentive-compatible adaptive multiple price list (MPL) in which they chose between the incentive and varying amounts of Money for Sure. We also used a second incentivized MPL between “Money for Sure” and a lottery to measure risk aversion. The 1,205 borrowers with valid survey responses were randomized to receive either the no-borrowing incentive, their choice on a randomly selected MPL question, or no reward (the Control group).

Allcott et al. use the field experiment to determine how well borrowers anticipate the extent of their repeat borrowing, and whether they perceive themselves to be time consistent. On those questions, they find that:

...on average, people almost fully anticipate their high likelihood of repeat borrowing. The average borrower perceives a 70% probability of borrowing in the next eight weeks without the incentive, only slightly lower than the Control group’s actual borrowing probability of 74 percent. Experience matters. People who had taken out three or fewer loans from the lender in the six months before the survey - approximately the bottom experience quartile in our sample - under-estimate their future borrowing probability by 20 percentage points. By contrast, more experienced borrowers predict correctly on average...

On average, borrowers value the no-borrowing incentive 30 percent more than they would if they were time consistent and risk neutral. And since their valuations of our survey lottery reveal that they are in fact risk averse, their valuation of the future borrowing reduction induced by the incentive is even larger than this 30 percent “premium” suggests.

So, borrowers on average anticipate their repeat borrowing, and they recognise that they are time inconsistent. Allcott et al. then use their experimental results, along with the results of the associated survey, to construct a theoretical model of payday loan borrowing. They then use their model to simulate the effect of various payday lending restrictions on borrower welfare, and find that:

Because borrowers are close to fully sophisticated about repayment costs, payday loan bans and tighter loan size caps reduce welfare in our model. Limits on repeat borrowing increase welfare in some (but not all) specifications, by inducing faster repayment that is more consistent with long-run preferences.

In other words, banning payday loans, or reducing the maximum size of payday loans, makes borrowers worse off. The flipside of that result is that the availability of payday loans actually makes borrowers better off. However, if policymakers are concerned about payday loans' potential negative effects, the most effective policy (in terms of borrower welfare) is to restrict the number of repeat loans that borrowers can take out. I suspect many policymakers would be surprised by that. However, an open question that is not addressed by this research is to what extent repeat lending restrictions simply force borrowers to alternative lenders like pawnbrokers (as the earlier research I discussed found).

Finally, Allcott et al. fire some shots at 'expert' economists:

Before we released the article, we surveyed academics and non-academics who are knowledgeable about payday lending to elicit their policy views and predictions of our empirical results. We use the 103 responses as a rough measure of “expert” opinion, with the caveat that other experts not in our survey might have different views. The average expert did not correctly predict our main results. For example, the average expert predicted that borrowers would underestimate future borrowing probability by 30 percentage points, which would imply much more naivete than our actual estimate of 4 percentage points.

Ouch! But it does illustrate the unanticipated nature of Allcott et al.'s results. If your model of payday loan borrowing starts from an assumption that borrowers don't anticipate their future borrowing behaviour, then you are more likely to support strong restrictions on payday lending. The poor performance of the experts in anticipating borrowers' naivete also suggests that Allcott et al. should be listened to over these other experts. It is unusual to include results like these in a paper (or even to do this sort of analysis). I wonder if Allcott et al. would have presented these results if the experts had agreed with them?

[HT: Marginal Revolution, last year]

Read more:

• What happens to pawnbrokers when you ban payday loans?

Price and prejudice

Economists distinguish between two different types of discrimination:

1. Taste-based discrimination, which involves bias against members of a particular group (this discrimination arises because of people's preferences for or against particular groups); and
2. Statistical discrimination, which involves treating people differently based on the group they belong to, because of differences in average characteristics between groups (this discrimination arises because of imperfect information about people, leading them to be treated as if all members of a particular identifiable group are the same).

As I noted in my recent review of Thomas Sowell's book Applied Economics, Sowell carefully explained that discrimination often imposes a cost on the person doing the discriminating. For example, if an employer discriminates against employees of a particular type, they may choose to employ others with lower productivity (and lower profitability for the employer) instead. The cost comes in the form of lower profits.

How much of a cost are discriminators willing to bear? That is the research question that is addressed in this 2018 article by Morten Hedegaard (University of Copenhagen) and Jean-Robert Tyran (University of Vienna), published in the American Economic Journal: Applied Economics (appears to be open access, but just in case there is an ungated version here). Hedegaard and Tyran use a field experiment among Danish high school students to estimate the willingness to pay to work with someone of the same ethnicity. Specifically, in the field experiment:

We hire 162 juveniles from secondary schools in Copenhagen, Denmark, with Danish-sounding and Muslim-sounding names to prepare letters for a large mailing and pay a piece rate. Workers are requested to show up for work twice in two consecutive weeks. In the first round, they work by themselves and we measure their individual productivity on the job. Before they come back for the second round, we call randomly selected workers on the phone and inform them that they will again do the same job but now have to work in teams of two. They are informed that they are paid the same piece rate as in round 1 and share earnings from team output in round 2 with the coworker. These randomly selected workers can choose whom to work with. The choice is between a candidate from the ethnic majority group and a candidate from an ethnic minority group. In treatment Info, we provide the decision maker with information about the individual productivity of the two candidates, i.e., the number of letters they prepared in round 1, and their first names as a marker of ethnicity... Rational decision makers who choose the less productive worker of the same ethnic type thus discriminate knowingly and deliberately.

Importantly, because Hedegaard and Tyran know the productivity of the workers from the first round. The sample is essentially split into threes. One person in each group of three is a decision-maker, and chooses which of the other two workers that they will work with in the second round. Hedegaard and Tyran ensure that the choice is between someone of the same ethnicity as the decision-maker, who has lower productivity, and someone of the opposite ethnicity, who has higher productivity. The 'price' of discrimination varies between decision-makers, depending on how more productive the opposite-ethnicity worker is than the same-ethnic worker that each decision-maker is offered. Hedegaard and Tyran can then test how much discrimination varies between decision-makers with higher and lower prices of discrimination. Based on their sample of 140 workers who completed both rounds, they find that:

...discrimination is common even at a substantial cost and that the tendency to discriminate is not different across ethnic types. We estimate that discriminators on average are willing to forego 8 percent of their earnings in round 2 to avoid a coworker of the other ethnic type. Our main result from treatment Info is that discrimination is highly responsive to the price of prejudice. Our best estimate is an elasticity of −0.9, i.e., we find that the probability to discriminate falls by about 9 percent if the price of discrimination goes up by 10 percent.

There is a lot to unpack there. First, people are willing to discriminate even if it costs them (which is consistent with Sowell's argument). Second, and a result that would surprise many people, ethnic majority and ethnic minority workers are equally likely to discriminate. Third, the elasticity is quite high - increasing the cost of discrimination reduces discrimination significantly.

Could it be that Hedegaard and Tyran are picking up statistical discrimination? That is, are the workers basing their decision on the average expected productivity of the workers of different ethnic groups? This seems unlikely, since both ethnicities are engaging in discrimination, and by definition both groups can't be less productive than each other (in fact, the Danish group is statistically significantly more productive). However, Hedegaard and Tyran explicitly test how important taste-based discrimination using a different treatment group, where the decision-makers were not provided with information about the round 1 productivity of the workers they could choose between (Hedegaard and Tyran refer to this as the 'NoInfo' treatment). They find that:

...statistical discrimination does not explain observed outcomes in NoInfo well. We find a large gap between observed earnings and earnings predicted by statistical discrimination (about 4 percent of total output). To account for taste-based discrimination, we use our estimate from treatment Info and find that it predicts well out of sample; about 40 percent of that gap is explained by animus-driven prejudice. Thus, our results suggest that prejudice is an important cause of ethnic discrimination in the workplace, and that it needs to be taken into account above and beyond the theory of statistical discrimination.

So, clearly there is a substantial amount of taste-based discrimination in this sample. To see just how much, consider that in the NoInfo experiment, 78 percent of decision-makers chose the same-ethnic worker, compared with just 38 percent in the Info experiment. Simply providing information about the price of discrimination was enough to reduce discrimination substantially.

Other than an interesting test of the relative important of the two types of discrimination, does this research provide some policy implications? It clearly demonstrates the existence of substantial ethnic bias or prejudice between workers. However, in terms of addressing the problem of discrimination this research suggests that, if there is some way to explicitly estimate the costs of discrimination, and make those explicit to decision-makers, discrimination could be reduced. Unfortunately, it is not clear how that would work as a solution in other real-world contexts.

Economists don't believe in civic honesty, but they should

This article by Alain Cohn (University of Michigan), Michel André Maréchal (University of Zurich), David Tannenbaum (University of Utah), and Christian Lukas Zünd (University of Zurich), published in the journal Science (open access), caused a bit of a stir last year. I've only just had the chance to have a proper read of it.

Cohn et al. conducted a field experiment to test the level of civic honesty in 355 cities across 40 countries. Specifically, they:

...turned in “lost” wallets and experimentally varied the amount of money left in them, which allowed us to determine how monetary stakes affect return rates across a broad sample of societies and institutions...

Wallets were turned in to one of five types of societal institutions: (i) banks; (ii) theaters, museums, or other cultural establishments; (iii) post offices; (iv) hotels; and (v) police stations, courts of law, or other public offices...

Our key independent variable was whether the wallet contained money, which we randomly varied to hold either no money orUS$13.45 (“NoMoney” and “Money” conditions, respectively)... Each wallet also contained three identical business cards, a grocery list, and a key.

They found that:

...our cross-country experiments return a remarkably consistent result: citizens were overwhelmingly more likely to report lost wallets containing money than those without. We observed this pattern for 38 of our 40 countries, and in no country did we find a statistically significant decrease in reporting rates when the wallet contained money. On average, adding money to the wallet increased the likelihood of being reported from 40% in the NoMoney condition to 51% in the Money condition (P < 0.0001).

Here's the key result graphically (note that New Zealand is among the countries with the highest level of civic honesty):

Cohn et al. also tried leaving an even larger amount (US$94.15) in wallets in three countries (the U.S., the U.K., and Poland), and that increased civic honesty even more. They then conducted a survey in those three countries, asking people what they expected to happen. They found that:

Respondents predicted that rates of civic honesty would be highest when the wallet contained no money (mean predicted reporting rate M = 73%, SD = 29), lower when the wallet contained a modest amount of money (M= 65%, SD = 24), and lower still when the wallet contained a substantial amount of money (M= 55%, SD = 29).

So, clearly the average person on the street doesn't think that people are as honest as they actually are. And then comes the real 'gotcha' moment in this paper. Cohn et al. ran a similar survey with a sample of "279 top-performing economists", and found that:

...respondents on average predicted that rates of civic honesty would be higher in the NoMoney and Money conditions (M=69%, SD=25 and M=69%, SD=21, respectively) than in the BigMoney condition (M = 66%, SD = 23). These predictions were again significantly different from the actual changes we observe across conditions (P < 0.001 for all pairwise comparisons).

So, apparently economists don't believe in civic honesty. So, what explains this unanticipated (at least, by the public in general, and by academic economists) result? Cohn et al. create a narrative model to explain, where:

...civic honesty is determined by the interplay between four components: (i) the economic payoff of keeping the wallet, (ii) the fixed effort cost of contacting the wallet’s owner, (iii) an altruistic concern for the owner’s welfare, and (iv) the costs associated with negatively updating one’s self-image as a thief (what we call theft aversion).

It is likely to be (iii) and (iv) that explain the desire to return the wallet. In relation to (iv), Cohn et al. rely on their three-country survey, and find that:

Respondents reported that failing to return a wallet would feel more like stealing when the wallet contained a modest amount of money than when it contained no money and that such behavior would feel even more like stealing when the wallet contained a substantial amount of money (P ≤ 0.007 for all pairwise comparisons)...

It's not the most persuasive evidence, particularly since it doesn't preclude (iii) from having an even larger effect. Some further research will be needed to unpack which of those two effects is largest.

However, this paper has highlighted an important issue. As I noted when I reviewed George Akerlof and Rachel Kranton's excellent book Identity Economics, the omission of identity from economic models is a potentially important omission. If the surveyed economists had recognised that the way that people view themselves is an important component of their utility function, and that self-perception as a 'thief' reduces people's utility, then perhaps these results would have been better anticipated, and the surveyed economists wouldn't have looked quite as foolish. Would it be too much to hope for that economists have learned from this?

[HT: Marginal Revolution, last year]

Street lighting and crime in New York City

This year in Waikato's Economics Discussion Group (EDG), we've adopted a new format. At each session, we discuss some recent research paper. At the most recent session, it was this recent NBER Working Paper by Aaron Chalfin (University of Pennsylvania) and co-authors, on street lighting and crime.

This paper was interesting, because it reported on a field experiment in New York City:

The field experiment described in this paper was conducted in the Spring and Summer of 2016 in NYC. Through a unique partnership between NYPD and MOCJ, we randomized the provision of street lights to the city's public housing developments, allowing us to avoid the potential challenges that could result due to spurious time trends as well as selection bias...

In order to select developments for the study, NYPD provided a list of 80 high-priority developments based upon their elevated crime rates and perceived need for additional lighting from among the 340 NYCHA developments in NYC. From this list, we randomized 40 developments into a treatment condition that would receive new lights and 40 developments into a control condition via paired random sampling, stratifying on each development's outdoor nighttime index crime rate and size in the two years prior to the intervention; treatment developments were then randomly assigned a lighting dosage.

Most prior studies have simply compared areas with more lighting with areas with less lighting. However, there is selection bias that is not accounted for, because areas with more lighting may differ from areas with less lighting, in ways that also affect crime. This study gets around that problem because the amount of lighting increase is randomised.

Chalfin et al. looked at the impact on night-time crime, and found that:

Accounting conservatively for potential spillovers, lighting reduces outdoor nighttime index crimes by approximately 36 percent and reduces overall index crimes by approximately 4 percent in affected communities, an outcome which is likely to be cost-beneficial, should the impact of lighting persist over time.

To be clear, the effects noted above are for a doubling of street lighting intensity. So, if you double streetlight intensity, you reduce outdoor night-time crime by 36 percent.

Our discussion in the EDG session highlighted a potential source of bias in the analysis, which the authors have only partially addressed. If you increase lighting in some areas, but leave other areas darker, some criminals will relocate their criminal activities from the well-lit areas to the less-well-lit areas. This will decrease measured crime in the well-lit areas, but increase measured crime in the less-well-lit areas. If the less-well-lit areas are the control areas for your analysis (and the well-lit areas are the treatment areas), then this displacement of crime will bias your comparison of treatment and control areas upwards. In other words, the impact of street lighting on crime will be overstated in this analysis.

I hadn't picked up the full implications of that point in my reading of the paper, so well done to the EDG students. Chalfin et al. did attempt to account for 'spillover effects' in their analysis:

Estimates are reported for on-campus crimes and, in order to test for spatial spillovers, for crimes that occur within a radius of 550 feet (two standard NYC blocks) from campus. While we do not detect evidence of spillovers...

So, they also test for whether crime increase outside of the treatment areas (but within two city blocks), but the effects they find are tiny. However, this attempt to detect spillovers will only pick up spillovers into neighbouring city blocks. So, if criminals relocate further than a block away from the well-lit area, the analysis isn't going to pick it up.

Finally, they find that day-time crimes also reduced (by 25% net of spillovers) in the treatment areas, although the impact is pretty imprecisely measured and is not statistically distinguishable from zero. This last point should make us very wary of over-interpreting the importance of the results from this paper. So, while the field experiment is a good approach, and certainly an advance on the previous literature, this doesn't provide strong evidence for the impact of street lighting on crime.

[HT: Marginal Revolution]

Even candy can't make young kids republican

There is a famous saying that: "A man who is not a Liberal at sixteen has no heart; a man who is not a Conservative at sixty has no head", attributed to Benjamin Disraeli (but, interestingly, also to many others). I don't think this statement has been rigorously empirically tested, but a recent paper in the journal Economic Inquiry (ungated earlier version here) by Julian Jamison (Consumer Financial Protection Bureau) and Dean Karlan (Yale University) looks at the youngest end of the age distribution - children (aged 4 to 15).

The paper involves probably the cutest field experiments possible - conducted on children at Halloween. The authors explain:

We set up two tables on the porch of a home for Halloween, one festooned with McCain campaign props in 2008 (Romney in 2012) and the other with Obama props. Children, at the stairs leading up to the porch, were told they could choose which side to go. Half of the children were randomly assigned to be offered twice as much candy for the McCain table (Romney in 2012), and half were offered an equal amount...

The experimental setup allows us to measure not just what proportion of children who trick-or-treat in this neighborhood support each candidate (as indicated by their choice of table), but also how elastic their support is, or, more precisely, how elastic their desire is to make a public statement of their support.

What did they find? In the 2008 experiment:

In the “equal candy” treatment, 79% of children chose the Obama table, reflecting the high level of support for the Democratic Party in New Haven, Connecticut. When offered twice the amount of candy to go to the McCain table, 71% of the children still chose the Obama table, though the difference is not statistically significant (Table 1)...

Children ages eight and under did not respond to the additional candy incentives — approximately 30% of children chose the McCain table in both treatment groups. Children ages nine and older however, were much more responsive to the candy incentive. The percentage of older children that visited the McCain table increased from 10% without the incentives to 30% with the incentives.

So, younger children were more firm in their preferences for Obama (they had less elastic preferences than older children). And in the 2012 experiment:

Our results are largely consistent with the results from 2008, suggesting that support for Obama in this context has not declined since 2008. Eighty-two percent of children chose Obama in the “equal candy” treatment, whereas 78% of children chose Obama when twice as much candy was offered at the Romney table.

As in 2008, for children ages nine and older, the double candy incentive appeared to encourage some Obama supporters to choose Romney. While 17% of older children chose Romney when offered equal candy, 31% of older children chose Romney when offered double candy. For children ages eight or under, the double candy incentive had the opposite effect: 18% chose Romney when offered equal candy, whereas 14% chose Romney when offered more candy.

So even bonus candy isn't enough to get young children to abandon their political allegiances. Older children are more easily swayed by a little extra sugar. If we extrapolate to adults then, does that explain pork barrel politics?